I loathe to link to the original post by Locwin, but must for my response to make sense.

A recent blog post (Sept 22, 2014; accessed Sept 24, 2014) by Ben Locwin addresses in the title and first line a study in Nature (Suez et al, 17 Sept 2014) titled “Artificial sweeteners induce glucose intolerance by altering the gut microbiota.” Locwin admits in the second paragraph that “indeed it may be true that gut microbiota can be influenced and adapt to large doses of artificial sweeteners.” He goes on to state that “this is unsurprising.” Indeed, he is absolutely correct. Reporting a temporal change in the gut microbiome following administration of any given artificial sweetener in an animal model or in human subjects would be trivial to the point of being boring. Even noting that the change propagated through time for some considerable period would be expected given prior work in diet and the microbiome.

Locwin proceeds to discuss a study with meat added to the diet, as his example. He then critiques the entire microbiome field by suggesting that the differences which are measured in these studies are analytically accurate yet practically unimportant. Formally, his critique follows the rhetorical device of an ‘overselling the microbiome’ repudiation; the distinction between correlation and causation, impractical mechanisms, and measurements of proxies. Individually, these critiques can be profitably applied to many microbiome studies. However, standing with Alexander Pope and Theodore Roosevelt, the critic demonstrates his utility by refining a field rather than simply taking potshots at the performances of others.

Locwin points to the inclusion of HbA1C measurements in Suez et al 2014 and then draws in a second study that used HbA1C as a proxy for metabolic dysfunction and noted a response to artificial sweeteners. Locwin implies that the second study is not relevant to human health and does not reflect poorly on the safety of artificial sweeteners. Locwin suggests that the signal in the study might be statistically insignificant (‘spurious’) and then implies that HbA1C is entirely irrelevant to metabolic dysfunction, particularly if the effect size is small (‘miniscule’). Drawing on an unspecified Mayo study of HbA1C, Locwin discusses the failings of HbA1C as a proxy for metabolic health at modest length and returns to his second study to describe the sample size (7 persons) as inadequate. Locwin never re-analyzes the original data, which might be appropriate, but baldly accuses ‘the authors [of] trying to find patterns in their data where none exist.’ In short, he must be calling for a retraction of this second paper.

Never does Locwin address the inclusion of multiple measures for metabolic dysfunction by Suez et al 2014, including direct glucose and insulin sensitivity in mice and in humans, as well as the waist-to-hip ratio in humans; stratified by BMI to prevent confounding.

Locwin’s blog post, which opened with the rhetorical move of asserting that avoiding artificial sweeteners was once again “fashionable,” returns to its roots by ignoring Suez et al 2014, instead broadly assaulting any criticism of artificial sweeteners. Locwin’s statements — “of course the data tell a different story” and a study which “attempted to correlate artificial sweeteners (aspartame) with brain tumors (glioblastoma and others) is considered entirely erroneous.” First, even according to this blog post, the uncited coauthors (Oney et al 1996, I presume) did find a correlation between aspartame and these brain tumors. The original authors explicitly addressed — successfully or not — the increased diagnostic rate for brain tumors, which the blog post posits as the true source of the increased cancer rates, with time as the confounding variable. Locwin has not found an overlooked factor — and fails to provide a substantial critique of the attempt to manage the confounder. Oney et al’s original observations did not hold in a large cohort study ten years later (Lim et al 2006); but there is no cause to insult the original authors.

Locwin provides a toy illustration apparently meant to illustrate the broader difficulties of statistical sampling and generalizations — but without actually addressing any of the real complexities of statistics nor the corrections which competent authors are expected to make in the course of research. General references to Seife’s popular work on the subject also does nothing to address real or implied failings of the individual papers being addressed; even those with small subject pools. Locwin raises two more topics — FODMAP and bloating, gluten sensitivity — once again irrelevant to the Nature paper he is addressing.

Finally, Locwin ends with a typical physician admonition dealing with sensitivity and specificity in diagnostics — that is, when the incidence of the disease is high, a diagnosis is more often correct. He applies it instead to the magnitude of effect as opposed to statistical significance. This abuses the folk wisdom and the research, both. He then trots straight into an assertion about calories and weight loss that would require a tome of clarifications to be verifiable, following that quickly with brazen declarations about public health (that the ‘biggest real risks’ to society are addressed by good driving, seatbelts, cardiovascular exercise and vaccinations).

In short, Locwin did not describe any relevant issues with Suez et al 2014; though, like any study, it has limitations. Allow me to briefly outline Suez et al 2014. A mouse model established an unexpected mechanism of action leading from the application of several different artificial sweeteners through 1) a common change in the microbiome to 2) well characterized gut biochemistry associated with metabolic disorders and finally 3) actual glucose intolerance — not a proxy measure. The described mechanism was clarified and reinforced by being abolished with antibiotics and transferred through infection of other mice from a different strain. In the mouse model, without a doubt, the effect is real. The statistics are sound to the extent that the mice were from the C57Bl/6 strain and the Swiss-Webster outbred strain, studied in a particular facility. We have no reason to expect that the experiment would fail elsewhere or with other arbitrarily selected outbred mice.

The study then moved to observed human subjects: 381 apparently healthy individuals. This is not a terribly small number. They were already enrolled in a nutritional study. The measures studied included waist-to-hip ratios, not simple proxies for metabolic disorders, and the microbiology was consistent with the animal models. A final study followed seven human individuals for one week, four of whom were after-the-fact categorized as ‘responders’ and three were not. A series of experiments followed their responses to glucose as well as the microbiology. These were consistent in the responders with the described mechanism of action in the mouse model. Cross-over experiments cycled back to the animal model, demonstrating that responses in animals from exposure to human microbes could be predicted by the observed responses in the humans. The presence of non-responders in the human population suggests that the effect size is much larger than would typically be measured in a representative sample of animals; appropriate stratification will be an important component of experimental design in this area.

Nothing about Suez et al’s published results are trivial or boring. That some weight and metabolism effects of the microbiome are transferred from humans to mice has been reported in the past; but the conservation of effect for artificial sweeteners demonstrated in the paper is far from guaranteed and the predictive power it yielded is very surprising. Clear mechanisms of action demonstrated in the study have been probed and disrupted; there is no magic correlation. Typically, in animal models, antibiotic administration also changes metabolism to increase adiposity; further exploration is needed to understand how these effects interact.

The mouse model would not stand on its own as relevant to humans, but Suez et al 2014 continues to a human study. In the context of the human study the mechanism by which artificial sweeteners cause glucose intolerance apparently generalize across representatives of at least two mammals. We might expect that the results hold for many omnivorous hindgut fermenting mammals. The time series studies with seven subjects are more than sufficient statistically because of the way causation can be inferred through time (prevents some kinds of confounding). In short, the statistical weaknesses that Locwin proposes are not found here. Finally, the effects carry all the way to waist-to-hip ratios in humans; there are no questionable proxies for metabolic compromise. Every objection Locwin raises is irrelevant to the study.

There are more studies to be done; for example, to determine how many ‘responders’ are present in which populations, how consistently individuals respond, on what time scales. Details of the mechanism will be extremely interesting — the specific microbes, the specific metabolites. The study does end at metabolic disease and does not progress to measured impacts on quality of life and mortality. There is no assurance that artificial sweeteners do not have a paradoxical effect individually or even at different life stages and in different dietary contexts — some people lose weight, others gain weight, etc. For the moment, however, this study provides mechanistic insight into the unexpected process by which some people experience the kinds of negative metabolic effects attributed to sugar while consuming artificial sweeteners.

Locwin’s denigration of Suez et al 2014 is completely unfounded. I leave further conclusions as an exercise for the reader.

DISCLAIMER: These opinions are mine alone and do not reflect the official policies or opinions of any agency or employer.

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Benjamin Kirkup

My microbiology education began primarily at a summer camp for oceanography, in the mornings. I proceeded to take a microbiology laboratory techniques class in high school. I did a short high school thesis on the ecological impact of food additives with regard to oral bacteria, and worked at SUNY Stony Brook on the ecology of bacteriocins. My undergraduate education was at Harvard. I did an undergraduate thesis, ecology but not particular to bacteria, and during my masters degree, phylogeny of bacterial RuBisCO among other things. My Ph.D. was at Yale University, the ecology of bacteriocins - continued. After a summer instructing undergraduate biology laboratory, I joined Civil and Environmental Engineering at MIT as a postdoctoral associate and had an opportunity to lecture on environmental microbiology. Working primarily on marine ecology, I also included some work on the bacteriocins. Following this, I joined the Army to help start a department which studies combat wound infections. Most recently, I have joined the Naval Research Laboratory as a research microbiologist.

This is a fascinating thread. Ben, as always, your commnts are highly valued. But….

Well, I don’t know, but I am having a lot of trouble finding the connection to the indoor microbiome. If there is one, could you help me by pointing it out? If it is not an obvious one, maybe you could explain it to me, a non-microbiologist (research architect) interested in the connection between indoor environmental exposures. Or maybe there are some lessons here that apply to our pursuit of an enhanced understanding of the link between indoor environment and indoor microbiome.

Actually I should explain. You said something to me (or wrote it) pointing out that the Mendeley collection was not including general review papers and other material about microbial ecology methods and studies. And I responded saying I thought the collection should focus only on studies of microbiology the built environment and not general studies.

I still think that is probably a good idea for the reference collection. However, for the blog I think we need to expand our coverage to include much more about the methods and techniques of microbial ecology and how they are applied. And this would include studies of any ecosystem, even if not microbiology of the built environment. So I have been asking people who work on microbiology of the BE to also post to this blog about their work and ideas if they relate in any way to microbial ecology OR building science even if they do not relate to the interface directly.

So I asked Ben to consider posting about this. And I think in order to catalyze deeper conversations about methods and tools, we need to include broader discussions here.

In a way, I would say it was you who convinced me of the possible value of doing this.